Common Mistakes in Statistics & Probability
328 common pitfalls across 82 concepts, including 82 recurring stuck points
These are the pitfalls students hit across all 82 statistics & probability concepts, from Mean, Median and Mode onward. Each entry names the concept it comes from, so you can tell a slip from a genuine gap and go straight to the explanation.
The procedure for mean is the easy part; the trap is forgetting to divide by the count after adding. Asking "Am I adding up all the values and dividing by how many there are?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Forgetting to divide by the count after adding — the mean is the sum per value, not the sum itself.
Counting the number of values wrong (off by one) — divide by exactly how many data points you added.
Using the mean on outlier-heavy data — when one value is far from the rest, switch to the median for a typical value.
The procedure for median is the easy part; the trap is finding the middle of the unsorted list. Asking "After sorting the data smallest to largest, what value sits exactly in the middle?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Finding the middle of the unsorted list — always sort smallest to largest before locating the middle.
Picking one middle value when is even — average the two middle values instead.
Using the position number as the answer — that is the position of the median, not its value.
The procedure for mode is the easy part; the trap is reporting the frequency instead of the value. Asking "Which value occurs more often than any other?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Reporting the frequency instead of the value — the mode is the data value that repeats most, not how many times it repeats.
Saying 'no mode' when several values tie — if two or more values tie for most frequent, the data is bimodal/multimodal and all are modes.
Forcing a mode on data where every value is unique — if nothing repeats, there is no mode.
The procedure for range (statistics) is the easy part; the trap is subtracting in the wrong order and getting a negative. Asking "Am I just subtracting the smallest value from the largest?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Subtracting in the wrong order and getting a negative — always do so the range is non-negative.
Forgetting to find the true max and min in an unsorted list — scan the whole list, do not assume the first and last entries are the extremes.
Trusting the range when an outlier is present — one extreme value inflates it, so switch to IQR for a robust spread.
The procedure for standard deviation is the easy part; the trap is forgetting the square root. Asking "Am I measuring how far values typically fall from the mean, in the data's own units?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Forgetting the square root — that gives variance, not standard deviation.
Dropping the squaring of deviations — positive and negative distances would cancel; square them first.
Dividing a sample by when you should divide by — sample SD () uses , population SD () uses .
The procedure for variance is the easy part; the trap is taking the square root and calling it variance. Asking "Am I averaging the squared distances from the mean (and not taking the square root)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Taking the square root and calling it variance — that result is the standard deviation; variance is before the root.
Averaging the deviations without squaring — raw deviations sum to zero, so square them first.
Mixing up the divisor — population variance divides by , sample variance () divides by .
The procedure for probability is the easy part; the trap is counting outcomes that are not equally likely. Asking "Are the outcomes equally likely, and am I asked how likely (not how many)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Counting outcomes that are not equally likely — the favorable-over-total rule needs equally-likely outcomes.
The gambler’s fallacy: thinking past results change the next independent event — a fair coin has no memory.
Reporting a count instead of a probability — the answer must be between 0 and 1 (or a percent), not a raw number of ways.
The procedure for sample space is the easy part; the trap is merging distinct outcomes. Asking "Have I listed every distinct outcome that could occur, with none missing or merged?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Merging distinct outcomes — and are different; treating them as one shrinks the sample space.
Forgetting an outcome — every probability divides by , so a missing outcome corrupts the answer.
Listing outcomes that are not equally likely without saying so — the favorable-over-total shortcut assumes equal likelihood.
The procedure for independent events is the easy part; the trap is multiplying probabilities for without-replacement draws. Asking "Does the first event happening change the probability of the second?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Multiplying probabilities for without-replacement draws — those are dependent; use the updated second probability.
Confusing independent with mutually exclusive — independent events can both happen (product nonzero); mutually exclusive cannot ().
Adding instead of multiplying for 'and' — use for 'or' on exclusive events, for 'and' on independent ones.
The procedure for conditional probability is the easy part; the trap is dividing by the whole sample space. Asking "Has some information already been revealed that shrinks the set of possible outcomes?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Dividing by the whole sample space — divide by , the known condition, which shrinks the denominator.
Swapping and — read carefully which event is the 'given.'
Assuming independence to skip the formula — only set if you have verified the events are independent.
The procedure for expected value is the easy part; the trap is averaging the outcome values without weighting by probability. Asking "Am I weighting each outcome by its probability and summing to get a long-run average?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Averaging the outcome values without weighting by probability — multiply each value by its chance first.
Letting the probabilities not sum to 1 — a complete set of outcomes must have probabilities adding to 1.
Treating as the result of one trial — it is the long-run average, which need not be an achievable single outcome.
The procedure for normal distribution is the easy part; the trap is applying the 68-95-99.7 rule to non-normal data. Asking "Is the data single-peaked, symmetric, and described by just a mean and a standard deviation?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Applying the 68-95-99.7 rule to non-normal data — the rule only holds for the symmetric bell.
Assuming any single-peaked data is normal — check for symmetry; a long tail means skew, not normal.
Confusing the curve's height with probability — for a continuous curve, probability is area under it over an interval, not the height at a point.
The procedure for z-score is the easy part; the trap is forgetting to divide by . Asking "Am I expressing this value as a number of standard deviations from its mean?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Forgetting to divide by — alone is a raw deviation, not a z-score.
Dropping the sign — a negative z means below the mean; the sign carries direction.
Using the wrong distribution's mean and SD — standardize each value with its own data set's and .
The procedure for permutation is the easy part; the trap is using a permutation when order doesn't matter. Asking "Does swapping two of the chosen items create a different valid outcome?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Using a permutation when order doesn't matter — that overcounts by ; use a combination instead.
Allowing repeats — assumes distinct items each used once; repeats need the counting principle.
Confusing and in — is the pool, is how many positions you fill.
The procedure for combination is the easy part; the trap is forgetting to divide by . Asking "Does rearranging the chosen items leave it the same selection?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Forgetting to divide by — that leaves a permutation count, which overcounts the orderings.
Using a combination when order matters — assignments and rankings need a permutation.
Mixing up and — note , so choosing 3 to keep equals choosing the others to drop.
The procedure for factorial is the easy part; the trap is setting . Asking "Am I counting the ways to arrange all distinct items, multiplying down to ?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Setting — by definition , which keeps the permutation/combination formulas consistent.
Multiplying only down to a wrong stopping point — go all the way to (e.g. , not ).
Confusing with or — factorial multiplies a descending run, not a square or a double.
The procedure for correlation is the easy part; the trap is saying correlation proves causation. Asking "Do the dots show a direction and tightness of pattern?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Saying correlation proves causation — association alone is not proof of cause.
Calling any upward pattern strong — strength depends on how tightly dots cluster around the trend.
Using correlation with categorical data — correlation needs paired numerical variables.
The procedure for scatter plot is the easy part; the trap is connecting scatter-plot dots automatically. Asking "Does each dot need both an x-value and a y-value?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Connecting scatter-plot dots automatically — dots show cases, not necessarily a path.
Using categories as if they were paired measurements — scatter plots need numerical x and y values.
Claiming causation from a visible trend — association alone does not prove cause.
The procedure for histogram is the easy part; the trap is leaving gaps between bars. Asking "Am I grouping one numeric variable into intervals and showing the count in each?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Leaving gaps between bars — histogram bins are continuous, so bars should touch (gaps mean a categorical bar graph).
Using unequal bin widths carelessly — equal-width bins keep bar heights comparable as counts.
Treating the tallest bar as the mean — it shows the most common bin (the mode region), not the average.
The procedure for box plot is the easy part; the trap is reading box width as a count of data. Asking "Am I summarizing or comparing distributions using min, Q1, median, Q3, and max?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Reading box width as a count of data — each section holds 25% of values; width shows spread, not frequency.
Forgetting outliers extend the whiskers only to non-outlier values — points beyond the fences are plotted separately.
Confusing the median line with the mean — the box plot shows the median, which the mean need not match in skewed data.
The procedure for quartiles is the easy part; the trap is splitting by equal value width instead of equal count. Asking "Am I splitting ordered data into four groups that each contain the same fraction of the values?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Splitting by equal value width instead of equal count — quartiles divide the data into equal numbers of points, not equal ranges.
Forgetting to order the data first — quartiles, like the median, require a sorted list.
Confusing Q2 with the mean — Q2 is the median (the 50th-percentile rank), which may differ from the average.
The procedure for interquartile range is the easy part; the trap is subtracting min from max instead of . Asking "Am I measuring the width of the middle half of sorted data, not the full extent?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Subtracting min from max instead of — the IQR uses the quartiles, never the extreme values.
Computing quartiles on unsorted data — order the data from smallest to largest before finding and .
Confusing with — the IQR is a width (a difference), not the median itself.
The procedure for data (abstract) is the easy part; the trap is treating a summary like the mean as the data. Asking "Is this the raw set of recorded observations, before any summary or conclusion?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Treating a summary like the mean as the data — data is the raw recorded values, not numbers computed from them.
Ignoring whether values are numbers or categories — you cannot average colors, so label the data type first.
Forgetting to record the question the data answers — context decides which graph and summary make sense.
The procedure for measurement is the easy part; the trap is writing a number without a unit. Asking "Have I named the one attribute and the unit before writing the number?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Writing a number without a unit — every measurement is a number paired with the unit of its attribute.
Measuring the wrong attribute — decide whether you need length, mass, time, or count before picking a tool.
Mixing units in one comparison — convert to a common unit before comparing 30 cm to 1 m.
The procedure for variability is the easy part; the trap is reporting only the mean and stopping. Asking "Am I describing how scattered the values are, separate from where they center?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Reporting only the mean and stopping — a mean with no spread hides whether the data is consistent.
Assuming equal means imply equal data — same center can come with very different variability.
Confusing high variability with a high average — spread measures distances from the center, not the center's size.
The procedure for noise is the easy part; the trap is explaining every fluctuation with a cause. Asking "Is this variation random with no consistent direction or cause?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Explaining every fluctuation with a cause — random noise has no cause, so don't invent one.
Reacting to one noisy data point as a trend — wait for a consistent direction before calling it a pattern.
Confusing noise with outliers — noise is widespread small wiggle; an outlier is one far-off value.
The procedure for signal vs noise is the easy part; the trap is calling any difference a real effect. Asking "Is the difference larger than the data's ordinary random fluctuation?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Calling any difference a real effect — compare it to the size of the random noise first.
Dismissing a true effect as noise — a difference much larger than the usual wiggle is likely signal.
Forgetting more data sharpens the call — small samples have so much noise that real signals hide.
The procedure for distribution (intuition) is the easy part; the trap is summarizing shape with only the mean. Asking "Am I asking about the overall shape of the values, not one summary number?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Summarizing shape with only the mean — a single number can't show skew, peaks, or gaps.
Assuming symmetry by default — check for a long tail before trusting the mean.
Ignoring the horizontal scale — the same counts on a stretched axis look like a different shape.
The procedure for center vs spread is the easy part; the trap is comparing groups by center alone. Asking "Have I reported both where the data sits and how spread out it is?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Comparing groups by center alone — equal means can hide very different spreads.
Pairing the wrong partners — use mean with standard deviation, and median with IQR.
Reporting spread without center (or vice versa) — a complete summary needs both.
The procedure for outliers (deep) is the easy part; the trap is eyeballing outliers without the fence. Asking "Does this value fall beyond or ?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Eyeballing outliers without the fence — compute and to flag them.
Deleting outliers automatically — first decide if it's an error, a rare event, or a meaningful exception.
Calling the maximum an outlier by default — the largest value isn't unusual unless it passes the fence.
The procedure for randomness is the easy part; the trap is expecting random sequences to alternate neatly. Asking "Is each single outcome unpredictable while the long-run rates stay fixed?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Expecting random sequences to alternate neatly — real randomness produces streaks and clusters.
Believing past outcomes affect the next independent one — randomness has no memory.
Confusing randomness (no pattern) with bias (a consistent tilt) — bias is predictable, randomness is not.
The procedure for chance is the easy part; the trap is calling a guaranteed event a matter of chance. Asking "Could this go more than one way, with no way to control which?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Calling a guaranteed event a matter of chance — chance needs at least two genuinely possible outcomes.
Thinking you can control a chance outcome — wishing for red doesn't change the spinner.
Jumping straight to a number — chance is the informal idea; probability is where the number comes in.
The procedure for probability as expectation is the easy part; the trap is expecting the exact expected count. Asking "Am I predicting a long-run count or share, not a single outcome?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Expecting the exact expected count — is the long-run average, not a promise for any one run.
Applying it to a single trial — probability-as-expectation describes many repetitions, not one outcome.
Confusing the predicted count with a probability — is a count, while stays between 0 and 1.
The procedure for events (formal) is the easy part; the trap is treating an event as one outcome. Asking "Am I naming a set of outcomes that make a yes/no question true?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Treating an event as one outcome — an event like 'even' is the whole set .
Forgetting the complement shortcut — uses .
Mixing up AND with OR — needs both true; needs at least one.
The procedure for dependence (statistical) is the easy part; the trap is multiplying for dependent events. Asking "Does knowing the first event occurred change the probability of the second?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Multiplying for dependent events — use instead.
Forgetting the pool changed — after a draw without replacement, update the counts before the next probability.
Equating dependence with causation — linked probabilities don't prove one causes the other.
The procedure for causation is the easy part; the trap is reading correlation as causation. Asking "Would deliberately changing X reliably change Y, not just co-occur with it?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Reading correlation as causation — co-movement alone never proves cause; check for confounders.
Ignoring lurking variables — a hidden third factor can manufacture a spurious link.
Forgetting direction — a link between X and Y might mean Y causes X (more police are sent where there is more crime), not that X causes Y.
The procedure for sampling bias is the easy part; the trap is believing a large sample cures bias. Asking "Did the selection method systematically include or exclude certain groups?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Believing a large sample cures bias — only fixing the selection method removes a systematic tilt.
Using convenience samples and generalizing — easy-to-reach groups rarely mirror the population.
Confusing bias with random error — bias is a consistent directional skew, not symmetric chance variation.
The procedure for representativeness is the easy part; the trap is assuming a big sample is representative. Asking "Do the sample's group proportions match the population's?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Assuming a big sample is representative — proportions must match, not just counts.
Checking only one variable — a sample can match on age yet miss on income.
Confusing the method with the result — random sampling helps, but you still verify the proportions match.
The procedure for law of large numbers (intuition) is the easy part; the trap is using it to predict short runs. Asking "Is the average of many independent trials settling toward the true mean as grows?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Using it to predict short runs — convergence is a long-run effect; 10 flips can stray far from 50%.
Slipping into the gambler's fallacy — the average approaches , but no single outcome is 'due'.
Expecting the count, not the average, to balance — it's the proportion that converges, while raw counts can drift apart.
The procedure for risk is the easy part; the trap is ranking by probability alone. Asking "Am I combining the probability of a loss with the size of that loss?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Ranking by probability alone — multiply by the loss amount so severity counts.
Ranking by severity alone — a catastrophic but near-impossible event may carry little expected loss.
Adding probability and loss instead of multiplying — Expected Loss is , a product.
The procedure for uncertainty is the easy part; the trap is forcing an exact answer onto an uncertain situation. Asking "Is precise prediction impossible because information is incomplete?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Forcing an exact answer onto an uncertain situation — use a range or probability instead.
Confusing uncertainty with randomness — uncertainty can come from missing info, not just random outcomes.
Treating an estimate as a guarantee — an estimate still carries uncertainty and should be hedged.
The procedure for prediction is the easy part; the trap is reporting a prediction as an exact number with no range. Asking "Am I stating a value I have not observed, with a sense of how uncertain it is?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Reporting a prediction as an exact number with no range - every prediction needs an uncertainty bound, not false precision.
Predicting far outside the data range and trusting it - patterns can break beyond where you have evidence.
Confusing a strong correlation with a guaranteed prediction - correlation tells you the relationship exists, not that the next case obeys it.
The procedure for model fit (intuition) is the easy part; the trap is judging fit only on the data used to build the model. Asking "Am I comparing a model's predicted values to the actual observed values to judge the gap?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Judging fit only on the data used to build the model - good fit must hold up on data the model has not seen.
Treating a perfect fit as the goal - a model that matches every point exactly is usually memorizing noise.
Ignoring the direction and pattern of residuals - if residuals curve, the model has the wrong shape even if the gaps are small.
The procedure for overfitting (intuition) is the easy part; the trap is picking the model with the lowest training error. Asking "Does the model do much better on the data it was trained on than on fresh data?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Picking the model with the lowest training error - overfit models always win on training; judge on held-out data.
Adding more parameters or wiggles to chase a better training score - extra complexity buys memorization, not generalization.
Calling any high-error model overfit - overfitting is specifically LOW training error with HIGH new-data error.
The procedure for underfitting (intuition) is the easy part; the trap is assuming poor accuracy always means overfitting. Asking "Does the model do badly even on the data it was trained on?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Assuming poor accuracy always means overfitting - if training accuracy is also poor, it is underfitting.
Keeping a model simple to avoid overfitting and ignoring that it never fit at all - too simple is its own failure.
Blaming the data when the model can't even match training points - a too-simple model misses real structure that is genuinely there.
The procedure for data visualization is the easy part; the trap is using the wrong chart type for the data. Asking "Am I turning data into a picture so a pattern is easy to see?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Using the wrong chart type for the data - bar graphs compare categories, line graphs show change over time.
Leaving off axis labels, titles, or a scale - an unlabeled graph can't be read correctly.
Assuming a fancier graph is a clearer graph - the best visualization is the one that makes the pattern obvious.
The procedure for misleading graphs is the easy part; the trap is trusting a graph because the data is real. Asking "Does the picture exaggerate or hide a difference that the actual numbers don't support?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Trusting a graph because the data is real - the distortion lives in the design choices, not the numbers.
Only checking the bars and ignoring the axis - the truncated axis is the most common trick.
Assuming any surprising graph is misleading - confirm a specific distortion (axis, interval, scale) before crying foul.
The procedure for scale distortion is the easy part; the trap is calling every nonzero axis a distortion. Asking "Is the axis baseline or interval spacing making a difference look bigger or smaller than it really is?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Calling every nonzero axis a distortion - some quantities (temperature, year) legitimately don't start at zero; ask whether it misrepresents the difference.
Comparing bar heights without reading the axis numbers - the height is only meaningful relative to the baseline.
Ignoring uneven intervals on an axis - jumps from 0,10,20 then 20,50,100 distort the slope of the trend.
The procedure for aggregation is the easy part; the trap is aggregating groups of different sizes by raw totals. Asking "Am I collapsing many individual values into a single summary number for the group?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Aggregating groups of different sizes by raw totals - compare proportions or rates when group sizes differ, not bare counts.
Trusting one summary number to tell the whole story - an aggregate hides spread, outliers, and subgroups.
Averaging numbers that are already averages without weighting - combine the underlying counts, not the summaries directly.
The procedure for normalization (statistics) is the easy part; the trap is comparing raw counts from groups of different sizes. Asking "Am I dividing by group size or rescaling so different-sized quantities can be compared fairly?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Comparing raw counts from groups of different sizes - divide each by its group size to get a fair rate first.
Forgetting the multiplier when rates are tiny - 'per 100,000' keeps rare-event rates readable instead of like 0.00003.
Normalizing by the wrong base - match the denominator to the population actually at risk, not just any total.
The procedure for proportional data is the easy part; the trap is comparing raw counts across groups of different sizes. Asking "Am I expressing a count as a fraction of its own total so different-sized groups compare fairly?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Comparing raw counts across groups of different sizes - convert each to a proportion of its own total first.
Reporting a count with no denominator - ' out of ' is the whole point; the base gives the count meaning.
Mixing up part-to-whole with part-to-part - a proportion divides by the total, a ratio divides by the other part.
The procedure for comparative statistics is the easy part; the trap is comparing only the means and ignoring the spread. Asking "Am I weighing two or more groups against each other rather than describing a single group?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Comparing only the means and ignoring the spread - two groups with equal averages can differ enormously in variability.
Declaring a difference real just because the numbers differ - a small gap may be noise, not signal.
Comparing groups of very different sizes by raw totals - use proportions or per-group rates to compare fairly.
The procedure for probabilistic thinking is the easy part; the trap is treating a high probability as a guarantee. Asking "Am I reasoning about an uncertain event in terms of likelihood and multiple outcomes, not a single certainty?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Treating a high probability as a guarantee - 'likely' leaves real room for the other outcome.
Demanding a single yes/no answer when the situation is uncertain - reason in likelihoods and plan for more than one branch.
Ignoring low-probability, high-impact events - rare doesn't mean it can't matter when it hits.
The procedure for decision under uncertainty is the easy part; the trap is choosing the option with the largest possible payoff. Asking "Am I choosing an action by weighing each option's outcomes against their probabilities?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Choosing the option with the largest possible payoff - weight it by probability; a big prize at low odds may have low expected value.
Ignoring risk and using expected value alone - two options with equal EV can differ hugely in how risky they are.
Letting one dramatic outcome dominate the choice - account for ALL outcomes and their chances, not just the memorable one.
The procedure for binomial coefficient is the easy part; the trap is using when order matters. Asking "Am I counting selections of from where order doesn't matter (or the matching expansion coefficient)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Using when order matters - if arrangement counts, use a permutation, which is times bigger.
Computing all of instead of canceling - cancels most factors; never multiply out giant factorials.
Forgetting - choosing which to keep equals choosing which to leave; use the smaller to compute.
The procedure for binomial distribution is the easy part; the trap is applying it when trials aren't independent or changes. Asking "Are there a fixed number of independent trials, each success/failure with the same probability, and I want a count of successes?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Applying it when trials aren't independent or changes - drawing without replacement is hypergeometric, not binomial.
Dropping the factor - you must count the orderings of the successes, not just multiply .
Mismatching the exponents - the success power is and the failure power is ; swapping them inverts the answer.
The procedure for sampling distribution is the easy part; the trap is using the population SD as the spread of the mean. Asking "Am I describing how a statistic (like ) varies across many samples, rather than how raw values vary?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Using the population SD as the spread of the mean - the sample mean's spread is the smaller standard error .
Confusing the data's distribution with the statistic's distribution - raw values and sample means have different spreads.
Thinking a bigger sample makes individual data less variable - bigger shrinks the spread of the MEAN, not of the data.
The procedure for central limit theorem is the easy part; the trap is claiming the raw data becomes normal. Asking "Am I claiming the distribution of a sample MEAN is approximately normal because the sample is large?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Claiming the raw data becomes normal - the CLT is about the distribution of the MEAN, not the individual values.
Applying it with a tiny sample from a very skewed population - is a rule of thumb; heavy skew needs even larger .
Forgetting the spread shrinks - the sample mean's SD is , not .
The procedure for confidence interval is the easy part; the trap is saying '95% chance the true value is in THIS interval'. Asking "Am I building a range from a sample that likely contains the true population value at a stated confidence?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Saying '95% chance the true value is in THIS interval' - the parameter is fixed; 95% refers to the procedure over many samples.
Using the data's SD as the spread of the estimate - the interval uses the standard error , not alone.
Picking the wrong critical value - for 95%, not for 90% or 99%; match to the confidence level.
The procedure for margin of error is the easy part; the trap is reporting the full interval width as the margin of error. Asking "Am I reporting how far an estimate might be from the truth as a single value (half the interval width)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Reporting the full interval width as the margin of error - the margin is HALF the width.
Using the data's SD instead of the standard error - the margin is , which shrinks with bigger .
Thinking margin of error covers bias or bad sampling - it only captures random sampling variability, not a flawed survey design.
The procedure for hypothesis testing is the easy part; the trap is treating 'fail to reject ' as 'prove true'. Asking "Am I deciding whether sample data is surprising enough to reject a specific stated claim about a population?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Treating 'fail to reject ' as 'prove true' - it only means insufficient evidence against it.
Choosing after seeing the data - set the significance level before testing to avoid cherry-picking.
Confusing the null and alternative - is the default 'no effect' claim; is what you suspect.
The procedure for p-value is the easy part; the trap is reading the p-value as the probability the null hypothesis is true. Asking "Am I computing the probability of data this extreme assuming the null is true (not the probability the null is true)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Reading the p-value as the probability the null hypothesis is true - it is the probability of the data given the null, not of the null given the data.
Concluding is true when p is large - a large p-value means insufficient evidence to reject, never proof the null holds.
Comparing the p-value to the wrong tail or forgetting two-sided - use for a two-sided test, doubling the one-tail area.
The procedure for type i and type ii errors is the easy part; the trap is swapping Type I and Type II. Asking "Am I classifying a wrong decision by comparing what the test concluded against what is actually true?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Swapping Type I and Type II - Type I rejects a TRUE null (false alarm), Type II misses a FALSE null (missed detection).
Believing you can shrink both errors at once for fixed sample size - lowering raises ; only more data shrinks both.
Calling a correct rejection an error - rejecting a false null is power (), the desired outcome, not a mistake.
The procedure for experimental design is the easy part; the trap is skipping random assignment but still claiming causation. Asking "Does the researcher actively assign subjects to treatments (rather than just observe what they already do)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Skipping random assignment but still claiming causation - only randomized assignment to treatments justifies a cause-and-effect conclusion.
Using one subject per treatment - replication (many subjects) is needed so one fluke result doesn't drive the conclusion.
Confusing the control group with 'do nothing' - the control gets a placebo or standard treatment so the only difference is the treatment itself.
The procedure for observational vs experimental studies is the easy part; the trap is claiming an observational study proved causation. Asking "Did the researcher assign the treatment to subjects, or only observe a group that already had it?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Claiming an observational study proved causation - without random assignment, only association can be claimed.
Thinking 'large sample' upgrades an observational study to causal - size doesn't remove confounders; only random assignment does.
Calling any study with two groups an experiment - if subjects already belonged to their group, it's observational.
The procedure for sampling methods is the easy part; the trap is equating a large sample with a representative one. Asking "Is the focus on the RULE for choosing who enters the sample (rather than how to assign treatments or compute a statistic)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Equating a large sample with a representative one - a biased method (convenience) stays biased no matter how big it gets.
Mixing up stratified and cluster sampling - stratified takes some from every subgroup; cluster takes everyone from a few chosen subgroups.
Calling systematic sampling random - picking every 10th person is only unbiased if the list has no hidden periodic pattern.
The procedure for geometric distribution is the easy part; the trap is using the binomial because both involve and . Asking "Am I counting the number of trials up to and including the first success (not the number of successes in a fixed set of trials)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Using the binomial because both involve and - the geometric has no fixed ; it counts trials until the first success.
Writing the exponent as instead of - the first trials are failures, so it's .
Forgetting the trials must be independent with constant - if changes or trials are dependent, the geometric model fails.
The procedure for chi-square test is the easy part; the trap is dividing by Observed instead of Expected. Asking "Are the data counts of cases falling into categories, being compared to expected counts (rather than means or continuous values)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Dividing by Observed instead of Expected - the formula is , scaling each gap by the expected count.
Using percentages or means as the data - chi-square requires raw category counts, not proportions or averages.
Using the wrong degrees of freedom - goodness-of-fit uses ; a two-way independence test uses .
The procedure for least squares regression line is the easy part; the trap is minimizing perpendicular or horizontal distances. Asking "Am I fitting a single straight line to two-variable numeric data by minimizing squared vertical distances?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Minimizing perpendicular or horizontal distances - LSRL minimizes squared VERTICAL distances ( residuals) only.
Confusing the slope with the correlation - they relate by ; has units, does not.
Extrapolating far outside the data's -range - the line is only trustworthy across the observed values.
The procedure for residuals is the easy part; the trap is computing predicted minus observed. Asking "Am I taking one point's actual value minus the line's predicted value to measure its individual miss?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Computing predicted minus observed - the standard is observed minus predicted, .
Expecting nonzero residuals to sum to something meaningful - for an LSRL the residuals always sum to zero, so use squared residuals to measure total error.
Ignoring a curved pattern in the residual plot - a clear curve means a line is the wrong model, even if individual residuals are small.
The procedure for coefficient of determination is the easy part; the trap is reporting when the question asks for . Asking "Am I reporting the fraction of 's variation explained by the linear model (a 0-to-1 number), not the slope or the correlation's sign?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Reporting when the question asks for - square the correlation; gives , not 0.7.
Reading as causation - it measures explained variation, never that causes .
Letting go negative or above 1 - it's a proportion between 0 and 1, so any value outside that range is an error.
The procedure for inference for regression is the easy part; the trap is treating a nonzero sample slope as proof of a population relationship. Asking "Am I testing whether the underlying population slope is nonzero (rather than just computing or describing the sample slope)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Treating a nonzero sample slope as proof of a population relationship - test against its standard error before concluding .
Using the wrong degrees of freedom - regression inference uses , not .
Forgetting the conditions (linearity, independence, equal spread, normal residuals) - the t-test is only valid when the regression assumptions hold.
The procedure for power of a test is the easy part; the trap is confusing power with . Asking "Am I asking for the probability of correctly rejecting the null GIVEN it is false (the detection rate)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Confusing power with - power conditions on being FALSE; conditions on being TRUE.
Thinking power and add to nothing useful - power , so a Type II error rate of 0.2 means power 0.8.
Believing a non-significant result proves no effect - a low-power test often misses real effects, so 'not significant' isn't 'no effect.'
The procedure for paired t-test is the easy part; the trap is treating paired data as two independent samples. Asking "Is every value in one group paired with exactly one specific value in the other (so I can form a difference per pair)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Treating paired data as two independent samples - form the per-pair differences and run a one-sample test on them.
Using - the paired test uses where is the number of PAIRS.
Using of one group instead of - the test uses the standard deviation of the differences, not of either original column.
The procedure for two-sample tests is the easy part; the trap is running a two-sample test on paired data. Asking "Are the two groups made of different, unrelated subjects with no natural pairing between them?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Running a two-sample test on paired data - if subjects are matched, use the paired t-test on differences instead.
Using a single pooled standard deviation by default - the two-sample t-test typically uses with separate variances.
Choosing a t-test for proportion data - compare proportions with the two-proportion z-test, not the t-test for means.
The procedure for compound probability is the easy part; the trap is adding for 'and' or multiplying for 'or'. Asking "Does the problem combine two or more events with 'and' (multiply) or 'or' (add minus overlap)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Adding for 'and' or multiplying for 'or' - 'and' multiplies; 'or' adds then subtracts the overlap.
Forgetting to subtract the overlap in an 'or' problem - use unless the events are mutually exclusive.
Using instead of for dependent events - when the first event changes the second, multiply by the conditional probability.
The procedure for experimental vs. theoretical probability is the easy part; the trap is reporting when the problem gives trial results. Asking "Does the probability come from reasoning about the possible outcomes (theoretical) or from counting what occurred in real trials (experimental)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Reporting when the problem gives trial results - if data is provided, use observed-over-trials, not the theoretical value.
Expecting experimental to equal theoretical in a few trials - they only converge over MANY trials (law of large numbers).
Thinking a deviation in 20 flips means the coin is unfair - small samples wander; only large, persistent deviations suggest bias.
The procedure for mean absolute deviation is the easy part; the trap is forgetting the absolute value. Asking "Am I averaging the ABSOLUTE distances of each value from the mean (not squared distances, not signed ones)?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Forgetting the absolute value - signed deviations from the mean sum to zero, so you must take first.
Squaring the deviations - that gives variance/standard deviation; MAD uses absolute value, not squares.
Dividing by the wrong count - divide the total absolute deviation by , the number of data values.
The procedure for two-way tables is the easy part; the trap is confusing joint, marginal, and conditional frequencies. Asking "Are two categorical variables being crossed in a grid so each cell counts a combination of one category from each?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Confusing joint, marginal, and conditional frequencies - joint is one cell's count (divide by the grand total for a joint relative frequency), marginal is a row/column total, conditional is a cell over a row (or column) total.
Dividing a cell by the grand total when a conditional is asked - condition on the given group by dividing by that row or column total.
Putting a numeric variable in the table - two-way tables cross two CATEGORICAL variables, not measurements.
The procedure for bayes' theorem is the easy part; the trap is treating as equal to . Asking "Am I given and a prior, and asked for the flipped ?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Treating as equal to - Bayes flips them, and the prior makes the two differ.
Ignoring the base rate (prior) - a rare condition keeps the posterior low even after strong evidence.
Using the wrong denominator - must total over ALL hypotheses (true and false), e.g. true positives plus false positives.
The procedure for line plots is the easy part; the trap is leaving out values with zero marks. Asking "Am I stacking a mark for each data point above its value on a number line to show frequency?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Leaving out values with zero marks - keep every value on the number line evenly spaced, even if its stack is empty.
Treating it like a category bar graph - line plots need evenly spaced NUMERIC values, not category labels.
Miscounting frequency - the number of stacked marks above a value IS its frequency, so count carefully.
The procedure for population vs sample is the easy part; the trap is calling the data you collected 'the population' just because it is all the data you have. Asking "Is this number describing every single member I care about, or only the subset I actually collected data from?" first is what keeps a correct-looking calculation from being attached to the wrong concept.
Calling the data you collected 'the population' just because it is all the data you have - the population is the full group you want to conclude about, usually larger than what you measured.
Mixing up the symbols and - is the population mean (whole group) and is the sample mean (the subset).
Assuming any sample represents the population - only a sample chosen to reflect the whole group can stand in for it; a biased subset cannot.